Use of Behavioral Economics in Repeat SARS-CoV-2 (COVID-19) Antibody Testing in Disadvantaged Communities: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Use of Behavioral Economics in Repeat SARS-CoV-2 (COVID-19) Antibody Testing in Disadvantaged Communities (NCT04901624), a randomized na study. The primary outcome is Attendance Rate at Time 2 SARS-CoV-2 Antibody Test.

2. Clinical Question

This is a question about participation in repeat testing, not a direct comparison of antibody status, infection, protection, or health outcomes. The registry record does not report a separate intervention-free comparator, nor does it specify whether the central scientific question was a main effect of message type, a main effect of incentive type, or an interaction between them. The posted arm-by-arm comparisons therefore describe differences between the listed combinations, while the broader factorial question cannot be fully reconstructed from the record.

3. Trial Design

The trial is registered as randomized, with a factorial model and no masking. Its official title is Use of Behavioral Economics in Repeat SARS-CoV-2 (COVID-19) Antibody Testing in Disadvantaged Communities. The sponsor is the University of Southern California. The registry lists phase as NA, enrollment as 2164, status as completed, a start date of 2021-06-29, and primary completion on 2023-06-03.

The four listed behavioral components were Family Risk Messaging, Personal Risk Messaging, Loss Protection, and Lottery Incentive. The posted arm descriptions pair one messaging approach with one incentive approach: Personal Risk + Loss Protection, Personal Risk + Lottery Incentive, Family Risk + Loss Protection, and Family Risk + Lottery Incentive. Randomization and factorial labeling describe the registered design, but the registry record does not report the allocation ratio, the randomization procedure, or the factorial analysis plan.

The primary endpoint concerns Time 2 test attendance among participants who attended Time 1 testing, over a timeframe of 6 months. Posted arm sizes for the endpoint are 308.0 for Personal Risk + Loss Protection, 285.0 for Personal Risk + Lottery Incentive, 286.0 for Family Risk + Loss Protection, and 203.0 for Family Risk + Lottery Incentive. These are the denominators associated with the posted attendance counts; they should not be read as a full participant-flow account. The registry record does not report reasons for nonattendance or explain the relationship between these endpoint denominators and the enrollment figure.

The record lists 2 outcome measures and 12 analyses. It identifies Social and Behavioral Determinants of Antibody Testing as a secondary outcome. It does not report masking details beyond none, implementation fidelity, or a fuller account of follow-up procedures.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: We drew a simple random sample of patient households without replacement from AltaMed registry. Each household sampled was contacted to identify eligibility and interest. Households met inclusion criteria if at least one member was a patient at AltaMed and the household contained at least one adult and at least one member 5 to 17 years of age.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Participants who attended Time 1 antibody testing.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Households who completed baseline survey and agreed to Time 1 antibody testing.

6. Primary Endpoint

The registry lists the primary outcome as Attendance Rate at Time 2 SARS-CoV-2 Antibody Test, measured over 6 months.

The primary endpoint is attendance at the Time 2 SARS-CoV-2 antibody test, measured over 6 months among participants who attended Time 1 antibody testing. It is recorded as a count of participants with an event, where the event is attendance. The posted counts are 123.0 of 308.0 in Personal Risk + Loss Protection, 84.0 of 285.0 in Personal Risk + Lottery Incentive, 129.0 of 286.0 in Family Risk + Loss Protection, and 78.0 of 203.0 in Family Risk + Lottery Incentive.

Attendance is relevant to a study designed to assess whether messaging and incentives encourage people to return for repeat testing. It measures participation in testing rather than the antibody result, whether a participant had an infection, or whether antibodies conferred protection. The registry’s stated population is participants who attended Time 1 testing, so the primary endpoint does not by itself describe testing uptake among people who did not attend the initial test.

For a binary outcome such as attendance, a group’s event count can be considered alongside the number at risk in that group. A risk difference expresses the contrast between the groups’ event proportions on an additive scale. General: this scale directly describes the difference in event probability, while uncertainty around the estimate remains important for judging how precisely the contrast is known. The registry record does not report additional endpoint details such as how attendance was verified or how missing Time 2 attendance information was classified.

7. Results Posted in the Registry

• Personal Risk + Lottery Incentive: 29.5% (84/285) versus 39.9% (123/308) on control; risk difference -10.5 percentage points (95% CI -18.1 to -2.8), risk ratio 0.74 (0.59–0.93); unadjusted two-proportion z-test p = 0.008.
• Family Risk + Loss Protection: 45.1% (129/286) versus 39.9% (123/308) on control; risk difference 5.2 percentage points (95% CI -2.8 to 13.1), risk ratio 1.13 (0.94–1.36); unadjusted two-proportion z-test p = 0.203.
• Family Risk + Lottery Incentive: 38.4% (78/203) versus 39.9% (123/308) on control; risk difference -1.5 percentage points (95% CI -10.2 to 7.1), risk ratio 0.96 (0.77–1.20); unadjusted two-proportion z-test p = 0.732.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted recalculations compare each of three listed combinations with Personal Risk + Loss Protection. For a binary endpoint, the event is attendance at Time 2 testing. The arm-level event count and denominator describe how many participants attended among those represented in the relevant endpoint group. General: a risk difference is the first group’s event proportion minus the reference group’s event proportion. A negative value means the first proportion is lower in that comparison; a positive value means it is higher. This gives an absolute contrast on the event-proportion scale.

For Personal Risk + Lottery Incentive, the recalculated risk difference was -0.105, with a confidence interval from -0.181 to -0.029. For Family Risk + Loss Protection, it was 0.052, with a confidence interval from -0.028 to 0.131. For Family Risk + Lottery Incentive, it was -0.015, with a confidence interval from -0.102 to 0.071. These estimates are identified as unadjusted recalculations from the posted summary counts. They do not incorporate covariates or a mixed-effects model unless those features are explicitly part of the calculation; the registry record does not report such adjustments for these recalculations.

A confidence interval represents a range of values reasonably compatible with the estimate under the calculation’s assumptions and sampling model. It communicates uncertainty as well as the direction and size of the estimated contrast. For a risk difference, zero represents equal event proportions. An interval that includes zero does not rule out no difference at the confidence level used; an interval wholly on one side of zero is less compatible with a zero difference under that same calculation. General: this interpretation is about statistical uncertainty, not the practical importance of a difference or whether an intervention should be used.

The registry separately reports Mixed Models Analysis results with a slope parameter, 95% confidence intervals, p-values, and a superiority classification. A mixed model is a general approach that can account for structure in observations, such as repeated measurements or grouping, when the model and data support that structure. The registry record does not report the model specification, the outcome scale for the slope, covariates, covariance structure, or the exact contrast coding. It is therefore not possible to identify which features the sponsor’s model incorporated or to translate its slope into an attendance probability from the registry record alone.

The reported mixed-model comparisons are not the same set of reference contrasts as the unadjusted recalculations. The registry lists Personal Risk + Loss Protection with Personal Risk + Lottery Incentive; Personal Risk + Lottery Incentive with Family Risk + Loss Protection; and Personal Risk + Lottery Incentive with Family Risk + Lottery Incentive. The corresponding reported slopes are 1.19, 1.46, and 1.11, with the confidence intervals and p-values described in the statistical interpretation. The record labels these as superiority analyses, but the meaning of the slope and the direction implied by the group ordering are not reported in the registry record. Caution is warranted in attaching a substantive direction to the slope without that information.

General: a p-value assesses how incompatible the observed data are with a specified null model, assuming the analysis model and its assumptions. It does not measure the probability that the null hypothesis is true, and it does not tell readers whether an effect is important. Here, the recalculated p-values are explicitly unadjusted. The record does not report whether or how the sponsor adjusted for multiple comparisons, so the reported p-values should not be assumed to control the chance of false-positive findings across all analyses.

Why can over-dispersion matter?

General: over-dispersion occurs when variability in the observed data exceeds what a statistical model expects. If a model underestimates that variability, its standard errors can be too small and its confidence intervals too narrow. Whether over-dispersion is relevant depends on the data and model. The registry record does not report an over-dispersion assessment, and the endpoint summaries do not establish whether it was present.

What can be concluded from the posted methods?

The record supports a transparent unadjusted comparison of attendance counts and separately gives the sponsor’s mixed-model results. It does not provide a complete statistical analysis plan, detailed model assumptions, missing-data handling, analysis-population definitions beyond the primary endpoint population, or multiplicity procedures. Those omissions limit independent reproduction and make it important to distinguish the recalculated contrasts from the sponsor’s reported model estimates.

10. Confidence Intervals and Precision

Precision is indicated by the confidence interval around an estimate: narrower intervals represent more precise estimates, while wider intervals leave more uncertainty about the contrast. Precision depends in part on the number of observations and the amount of variability, as well as on the analysis model. A point estimate alone cannot show how much uncertainty surrounds it.

The recalculated risk difference for Personal Risk + Lottery Incentive versus Personal Risk + Loss Protection was -0.105, with a confidence interval from -0.181 to -0.029. This interval is on the negative side of zero. For Family Risk + Loss Protection versus the reference, the estimate was 0.052 and the interval ranged from -0.028 to 0.131. For Family Risk + Lottery Incentive versus the reference, the estimate was -0.015 and the interval ranged from -0.102 to 0.071. The latter intervals include both zero and values in either direction, reflecting uncertainty about the contrast.

The posted arm denominators are 308.0, 285.0, 286.0, and 203.0, and the corresponding attendance counts are 123.0, 84.0, 129.0, and 78.0. These values provide context for the precision of the arm comparisons, but the registry record does not provide a full account of missing outcome information or participant flow. No confidence interval for an arm’s attendance proportion is listed separately in the record.

The sponsor’s mixed-model confidence intervals are reported for slopes, not for the recalculated risk differences. They are 0.42 to 1.97, 0.68 to 2.24, and 0.26 to 1.96 for the three listed analyses. Because the slope scale and model details are not reported in the registry record, these intervals cannot be directly compared with the risk-difference intervals as though they measured the same quantity. Their interpretation depends on the sponsor’s model and parameter definition.

Confidence intervals do not account automatically for every possible source of uncertainty. In particular, the registry record does not report adjustment for multiple comparisons, sensitivity analyses, or how missing data were handled. Statistical precision within a model should not be mistaken for certainty about the model’s assumptions or the result’s broader meaning.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s own original design assumptions. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For these binary attendance comparisons, the figures are participants per arm, not total events.

The 80% power column gives the number of participants per arm used in the planning calculation to provide an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the model assumptions hold. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design-planning quantities, not guarantees about what a future study will find.

For example, planning for 100% of the observed effect in the Personal Risk + Lottery Incentive comparison gives 324 participants per arm for 80% power and 434 participants per arm for 90% power. Planning for 75% of that observed effect gives 587 and 785 participants per arm, respectively. The other comparisons have their own figures because the observed effects differ. The registry record’s original sample-size justification and design assumptions are not reported in the registry record.

Smaller effects are harder to distinguish from random variation, so the planning figures increase when the calculation targets a smaller fraction of the observed effect. This pattern is visible across the rows for 100%, 75%, and 50% of the observed effect. The figures are illustrations conditional on the calculation assumptions, rather than a claim about the adequacy of the completed trial or an estimate of its chance of success. This is not observed power.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.399; treatment proportion p₁ = 0.295; average p̄ = 0.347.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6732 = 1.3195.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6691 = 0.5632.
4. n = (1.3195 + 0.5632)² / (-0.1046)² = 323.9, rounded up to 324 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.399350649350649                          # control proportion
p1 <- 0.294736842105263                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4901624)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 324 (80% power), 434 (90% power)
 75% of observed effect: n per arm = 587 (80% power), 785 (90% power)
 50% of observed effect: n per arm = 1,341 (80% power), 1,795 (90% power)
power.prop.test: 323.9 
Simulated power at n = 324 per arm: 0.808 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Analyses Reported by the Sponsor

The registry includes sponsor-reported Mixed Models Analysis results as slopes, with 95% confidence intervals and p-values. The listed results are 1.19 (0.42 to 1.97), p = 0.003, for Personal Risk + Loss Protection and Personal Risk + Lottery Incentive; 1.46 (0.68 to 2.24), p < 0.001, for Personal Risk + Lottery Incentive and Family Risk + Loss Protection; and 1.11 (0.26 to 1.96), p = 0.01, for Personal Risk + Lottery Incentive and Family Risk + Lottery Incentive. Each is labeled a superiority analysis.

The simple recalculations use the posted event counts and denominators to estimate unadjusted risk differences against Personal Risk + Loss Protection. They are not necessarily the same estimand or model as the sponsor’s mixed-model contrasts. The registry record does not explain the slope scale or give the model specification needed to reconcile the estimates.

Because the record flags a discrepancy, the sponsor’s own analysis takes precedence as the trial’s reported analysis. The recalculations remain useful for describing the arm counts and showing what an unadjusted risk-difference comparison yields, but they should not be presented as a correction to or replacement for the sponsor’s analysis. The registry record does not report enough detail to determine the source of the discrepancy.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 12 analyses and 2 outcome measures, and identifies Social and Behavioral Determinants of Antibody Testing as a secondary outcome. It also reports three mixed-model comparisons and three unadjusted recalculations against the reference arm. Multiple outcomes and comparisons create a multiplicity issue: when many hypotheses are examined, the chance of finding at least one apparently notable result can increase even if no underlying differences exist. General: adjustment methods can address this issue, but they may alter the interpretation of individual p-values and confidence intervals.

The registry record does not report whether the sponsor prespecified a hierarchy of comparisons, adjusted for multiplicity, or treated the analyses as exploratory. It does not report a statistical analysis plan or explain how the 12 analyses relate to the 2 outcome measures. The unadjusted recalculated p-values should therefore be understood as unadjusted; no family-wise or false-discovery control can be inferred. The mixed-model p-values should likewise not be assumed to have multiplicity control when none is described.

Missing-data handling is also not reported in the registry record. The endpoint population is described as participants who attended Time 1 antibody testing, but the record does not describe how missing Time 2 attendance was classified, whether any participants were excluded from the endpoint analysis, or how incomplete follow-up was addressed. The listed arm denominators do not by themselves explain losses between testing occasions or the disposition of all enrolled participants.

The record does not report the analysis populations for each of the sponsor’s mixed-model comparisons, whether analyses followed intention-to-treat principles, or whether participants were analyzed according to assigned combinations regardless of intervention exposure. It also does not report prespecified subgroup analyses, the factorial main-effect and interaction analyses, or handling of protocol deviations. These omissions limit assessment of selective reporting and reproducibility. The registry’s completion status and posted outcome numbers do not substitute for a detailed account of analysis decisions.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse events and other adverse events by group. For Personal Risk + Loss Protection, 626 were at risk and 0 were affected by serious adverse events; 626 were at risk and 0 were affected by other adverse events; deaths were 0. For Personal Risk + Lottery Incentive, the corresponding figures were 550 at risk, 0 serious, 550 at risk, 0 other, and 0 deaths. For Family Risk + Loss Protection, they were 539 at risk, 0 serious, 539 at risk, 0 other, and 0 deaths. For Family Risk + Lottery Incentive, they were 449 at risk, 0 serious, 449 at risk, 0 other, and 0 deaths.

These are the adverse-event figures reported in the registry record. They describe the listed risk denominators and reported affected counts; they do not establish that no events occurred outside the categories or observation periods captured by the record. The registry does not list serious adverse event terms and does not provide further detail about event collection, follow-up duration, or ascertainment. The record reports 0 deaths in each group. These figures should be read as safety reporting, not as evidence about the primary attendance endpoint or a general conclusion about safety.

16. What the Result Does, and Does Not, Mean

The primary outcome addresses whether participants who attended Time 1 testing returned for a Time 2 SARS-CoV-2 antibody test. The posted arm counts show that attendance varied across the four message-and-incentive combinations. The unadjusted recalculation found a negative risk difference for Personal Risk + Lottery Incentive relative to Personal Risk + Loss Protection, while the confidence intervals for Family Risk + Loss Protection and Family Risk + Lottery Incentive relative to that reference include zero. These are descriptions of the posted attendance data and their uncertainty, not conclusions about antibody status or infection.

The registry also reports mixed-model slopes for three comparisons, each labeled as a superiority analysis. Because the record does not explain what the slope represents or specify the model, those results cannot be translated confidently into absolute attendance differences. The flagged discrepancy means the sponsor’s own analysis takes precedence over the simple recalculations as the trial’s reported analysis. The two kinds of estimates should remain distinct rather than being blended into a single interpretation.

The study is about behavioral approaches to repeat testing in disadvantaged communities. Its endpoint is participation in testing, not the accuracy of antibody tests, the presence of antibodies, immunity, infection risk, or health outcomes. The registry’s brief summary describes potential reasons why repeated testing may be of interest, but the posted primary endpoint does not measure those broader consequences.

Statistical uncertainty and reporting gaps matter. The registry record does not report the full analysis plan, multiplicity handling, missing-data methods, or sufficient detail to interpret the mixed-model slope. Those omissions make it difficult to assess the robustness of the inferential results independently. The record does not support a general claim that a particular behavioral component will reliably increase repeat testing in other settings. It describes the registered trial’s attendance endpoint and reported analyses, with the limits noted above.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how behaviorally framed messages and incentives can be evaluated when the outcome is participation rather than a biological measurement. Repeat-test attendance is a binary event that can be described with counts, proportions, and absolute differences. Showing those quantities alongside uncertainty helps distinguish the observed pattern from the precision with which it is estimated.

The factorial label also highlights the importance of separating comparisons between combinations from estimates of component effects. Comparing Personal Risk + Loss Protection with Family Risk + Lottery Incentive changes both message framing and incentive type at once. A difference between such combinations cannot by itself isolate the contribution of either component. The registry record does not report the factorial main-effect or interaction analysis, so the component-level question remains unresolved in the posted information.

The record also illustrates why the analysis scale and model description matter. The recalculated risk differences are readily interpretable as absolute contrasts in attendance proportions, while the sponsor’s mixed-model slopes are not interpretable on that scale without a parameter definition. The discrepancy between the recalculations and sponsor analysis makes transparent reporting especially important: readers need enough information to understand the outcome, contrast, model, and analysis population.

Finally, planning illustrations based on an observed effect should be read cautiously. They show how required per-arm enrollment changes under stated assumptions and target effects; they do not recover the original trial’s design rationale. The registry record’s missing details about multiplicity, missing data, and the statistical plan reinforce the value of complete methods reporting for behavioral trials.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this trial follow from the registry record. First, the primary endpoint is attendance among participants who attended Time 1 testing. It therefore does not describe uptake among people who did not attend the initial test, and it cannot establish whether the interventions affected antibody results or health outcomes. The record does not explain how Time 2 nonattendance or missing attendance information was handled.

Second, the registered factorial structure includes combinations of messaging and incentives, but the registry record does not report analyses that separate the component effects or assess interaction. Contrasts between combinations may change both components at once. Without a reported factorial analysis, it is not possible to attribute any observed contrast to one component alone.

Third, the study was unmasked, and the interventions were behavioral. The registry record does not describe how messages and incentives were delivered, whether delivery was consistent, or whether intervention exposure was measured. These details would help readers understand how closely the tested approaches corresponded to the registered intervention labels.

Fourth, the record does not provide a full statistical analysis plan, the mixed-model specification, the meaning of the slope parameter, multiplicity procedures, or the handling of missing data. It also does not report subgroup methods or a complete participant-flow account. The discrepancy between the recalculated count-based contrasts and sponsor analysis cannot be resolved from the registry record.

Finally, the title identifies disadvantaged communities, but the registry record does not give enough population detail to evaluate how broadly the findings may apply. The available results concern attendance for repeat antibody testing in the registered study, rather than testing behavior in every community or setting.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Use of Behavioral Economics in Repeat SARS-CoV-2 (COVID-19) Antibody Testing in Disadvantaged Communities — NCT04901624.
• Registry record last updated 2024-08-14; status last verified 2024-07.
• Results first posted 2024-08-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04901624 is a completed randomized factorial study sponsored by the University of Southern California, with no masking. It lists enrollment of 2164 and investigates behavioral approaches to repeat SARS-CoV-2 antibody testing in disadvantaged communities. The primary endpoint is attendance at Time 2 testing over 6 months among participants who attended Time 1 testing.

The four listed combinations pair Personal Risk or Family Risk messaging with Loss Protection or a Lottery Incentive. The posted arm counts support unadjusted risk-difference recalculations, while the registry separately reports three mixed-model slope analyses. The record flags a discrepancy, so the sponsor’s own analysis takes precedence as the trial’s reported analysis. The slope scale and model details are not reported in the registry record.

The record also lists Social and Behavioral Determinants of Antibody Testing as a secondary outcome. Details about multiplicity, missing data, the original sample-size assumptions, and the full analysis plan are not reported in the registry record.